Correcting Travel-Driven Under-Diagnosis in Environmental Health Record Studies

Many studies of pollution and health are retrospective cohorts: researchers reconstruct who lived near a hazard from routinely collected medical records, then compare disease rates. These records only capture a disease when the patient reaches a clinic. Pollution sources such as wastewater canals, agricultural runoff, and industrial sites tend to sit in rural or peripheral areas, and those same areas are often far from care. People living near the hazard may therefore be diagnosed later, less often, or only once they are already dying. A naive analysis can then make a real toxic effect look weaker or shifted in time, or make a harmless hazard look dangerous. This proposal builds and tests an estimator that treats each patient's stream of ordinary clinic visits as a direct measurement of how visible that patient is to the record system. It uses that stream to separate "far from care" from "close to the hazard."

The opportunity is that each ingredient already exists in a separate literature, but nothing in the compiled material connects them. Environmental epidemiologists have built careful exposure surfaces. Access researchers have built validated travel-time surfaces. Researchers who study bias in medical records have documented how missing documentation gets mistaken for health. No one has asked how the access gradient corrupts the exposure gradient inside a records-based cohort, or tested a correction against known ground truth.

Core Claim

In a retrospective cohort built from electronic health records (the clinical notes, codes, and lab results generated during routine care), the recorded date of a diagnosis is the true onset date plus a detection delay. That delay grows with travel friction, meaning the real cost in time and effort of reaching a facility. When friction is correlated with environmental exposure, standard exposure–outcome estimates are biased, and the bias is not removed by simply adding travel time as a covariate.

The reason is structural. In a time-to-diagnosis analysis, friction does more than scale the rate of recorded events. It shifts when events are recorded, censors people who die or leave before detection, and sorts late presenters into apparently "mild" or apparently "severe" categories depending on what was documented. Our claim is that modelling detection as a separate process can recover the true exposure effect where covariate adjustment and cohort restriction do not. That process is driven by each patient's observed encounter intensity, estimated from visits unrelated to the outcome. The claim is falsifiable: if friction-adjusted Cox regression already recovers injected effects in realistic semi-synthetic cohorts, the extra machinery is unnecessary, and we will report that.

Why this is not already done

Three lines of work each touch two of the three directions, and each stops short in a specific way.

On the exposure side, Bayesian Methods for Modeling Cumulative Exposure to Extensive Environmental Health Hazards models hazard intensity along a 4,400 km canal network with a log-Gaussian Cox process, a random field describing how hazard strength varies along the network. It integrates that field against distance-decay kernels and finds that risk falls to roughly zero beyond 200 m, where nearest-distance models had suggested a broad decline. Its outcomes come from a dedicated field survey, so ascertainment is by design uniform. Our setting is the opposite: outcomes come from records whose completeness varies across space. Creating a Spatial Vulnerability Index for Environmental Health weights pollutant and climate sub-indices by their rank correlation with area-level mortality. Mortality is the one outcome least affected by access, and the analysis is ecological, so it never meets individual-level under-diagnosis.

On the access side, Income disparities in driving distance to health care infrastructure in the United States and Beyond distance: integrating economic burden into large-scale primary healthcare accessibility analysis supply the method we reuse. The first computes road-network driving distances on a synthetic population. The second builds a 1×1 km travel-friction surface for mainland China that matches navigation-API travel times with $R^2$ of 0.79 to 0.92. Neither links friction to recorded health outcomes. Predicting the Travel Distance of Patients to Access Healthcare using Deep Neural Networks treats travel distance as something to predict from claims, not as something that distorts what claims record. It also motivates a constraint: residence there has to be imputed from low-stakes visits, so exposure itself is misclassified.

On the records side, two papers both motivate and constrain the work. Bias Associated with Mining Electronic Health Records shows the "documentation paradox": patients who died rapidly in the emergency room had no documented symptoms, were scored as lowest risk, and gave that class nearly double the mortality of the next class. Filtering to well-documented cases then removed the sickest patients. Cohort design and natural language processing to reduce bias in electronic health records research shows that restricting to patients with regular primary care visits removes an artificial spike in incidence and improves calibration. Both treat missingness as an artifact of the institution or of documentation. We treat it as a spatial process with a measurable cause.

Research Program

The model has two linked parts. For patient $i$ with environmental exposure $E_i$ and covariates $X_i$, the latent onset time has hazard

$$\lambda_i(t) = \lambda_0(t)\exp(\beta E_i + \gamma^\top X_i),$$

where $\beta$ is the exposure effect we want and $\lambda_0$ is a baseline hazard. Onset is recorded at the first subsequent encounter at which the condition is detected. Encounters arrive at rate

$$\mu_i(t) = \exp(\alpha_0 + \alpha_1 F_i + \alpha_2^\top Z_i(t)),$$

where $F_i$ is travel friction from the residence to the nearest relevant facility, and $Z_i(t)$ holds time-varying drivers of visits such as age, insurance, and provider continuity. Detection then happens at each such encounter with probability $p$. The key ingredient is that $\mu_i$ is estimated from each patient's encounters for unrelated reasons (vaccinations, minor infections, refills), which every records database contains. Detection delay is therefore identified from data rather than assumed. Death from records linked to vital statistics, where such linkage exists, enters as a competing event that can occur before detection. That is exactly the route by which the documentation paradox arises.

Exposure $E_i$ comes from an environmental assessment surface. In the main setting this is a distance-decay-weighted hazard intensity in the style of the canal-network model. Friction $F_i$ comes from a least-cost travel surface. Residence uncertainty is propagated by sampling candidate residences from the imputation distribution, analogous in spirit to how Predicting the Activity of Unidentified Chemicals in Complementary Bioassays from the HRMS Data uses Monte Carlo sampling to carry probabilistic fingerprints forward rather than thresholding them.

We deliberately do not plug chemical toxicity predictions into the outcome model. The Tox21 work cited in the file shows that such predictions are noisy for most assays, so they would add a large error source orthogonal to the question asked here.

The work has three stages. First, we build a semi-synthetic benchmark on real geographies: the China friction surface and the US synthetic population with road networks, with hazard maps placed both at real peripheral locations and at locations deliberately uncorrelated with friction. Second, we simulate cohorts with known $\beta$. Visit processes in these cohorts are calibrated so that visit frequency falls with distance at realistic rates, and frailty is heterogeneous so that late presenters are sicker. Third, we apply the estimators to a real claims-type database with geographic identifiers, together with internal checks that need no ground truth.

Baselines

The naive reference is a Cox proportional hazards model of recorded diagnosis on exposure and standard covariates, run on all patients with any record. This is the model most environmental records studies actually fit. Any method should beat it. If it is already unbiased in the semi-synthetic cohorts, the premise fails.

The strongest simple competitor is the same Cox model with travel friction added as a flexible covariate (a spline in least-cost travel time), alongside a propensity score for exposure in the style of Long-Term Survival in Men With High Grade Prostate Cancer. There, composite propensity scores balanced older, sicker patients channelled into conservative care. Here they balance age, income, and urbanicity against exposure. This baseline is strong because it uses the same validated friction surface and the same covariates, and if detection only scaled the rate of recorded events it would be sufficient.

The second strong competitor is design-based restriction: only patients meeting a C3PO-style requirement of at least two primary care visits within one to three years. This is the cohort design from Cohort design and natural language processing, which reports Pooled Cohort Equations calibration error of 0.012 to 0.030 in the restricted cohort versus 0.028 to 0.046 in convenience samples. That is the only reported number in the file for a bias-reducing cohort design. For the specific target here, bias in an environmental exposure effect under friction-dependent ascertainment, there is no reported result found on Lacuna for any method.

Fairness is ensured by construction. Every estimator sees the same cohort extract, the same exposure surface, the same friction surface, and the same covariates. Spline degrees of freedom and propensity model choices for the baselines get the same cross-validated tuning budget as the hyperparameters of the detection model.

The key ablation keeps our full two-part model but replaces the encounter-intensity estimate $\mu_i$ with a function of friction alone ($\alpha_2 = 0$, no use of unrelated visits). This isolates whether the visit stream, rather than the two-part structure, carries the correction.

Beating a baseline means two things in the semi-synthetic cohorts with exposure correlated with friction: lower absolute bias in $\hat\beta$, and 95% interval coverage within two points of nominal where the baseline falls short. It also requires no loss relative to the baseline when exposure and friction are uncorrelated.

Why not just…?

Why not just adjust for travel time as a covariate? This is the real threat, and the proposal is designed so it can win. If detection merely scales the recorded event rate by a factor depending on friction, a log-link model absorbs the scaling and the covariate fix is adequate. It fails if detection delays events in time, interacts with frailty, or competes with death before diagnosis. In those cases the recorded-event hazard is no longer proportional in friction, and patients who die undiagnosed in remote areas disappear rather than being down-weighted. The semi-synthetic cohorts vary exactly these features: pure rate scaling, pure delay, delay with frailty, and delay with competing death. That tells us in which regimes the covariate fix is enough. If it matches our estimator throughout, we will recommend it.

Why not just restrict to patients with regular primary care? Restriction removed the incidence spike in C3PO, but it selects on visit frequency, which is itself driven by friction. In a remote exposed area, the people who pass the filter are the unusually well-connected minority, so the analysis is conditioned on a variable caused by geography. The pneumonia study's finding that filtering to well-documented cases suppressed mortality in the most severe class (Bias Associated with Mining Electronic Health Records) is the same failure mode. The authors of the C3PO paper also note that their restricted cohort lost demographic diversity. Our experiments measure both the bias and the fraction of the exposed population excluded.

Why not just use mortality, which everyone eventually records? Hard outcomes are nearly immune to access-driven under-diagnosis, which is why we use them as an anchor in the experiments below. But many environmental endpoints of interest are chronic, non-fatal diagnoses: endocrine, renal, developmental. Mortality also folds in delayed treatment caused by distance, the "second delay" that drives fatality differences in Spatial and temporal fluctuations in COVID-19 fatality rates in Brazilian hospitals. Mortality therefore confounds toxicity with access in a different way rather than escaping the problem.

Why not just use straight-line distance for friction? The material already rules this out. Straight-line distance underestimates real travel burden in rugged and flooded terrain (MamaCare AI), and least-cost surfaces match observed travel times far better (Beyond distance). We include straight-line friction only as a sensitivity arm.

Proposed Experiments

The first experiment is the semi-synthetic grid. Injected $\beta$ takes values of zero, modest, and large. The correlation between exposure and friction is set to near zero, moderate, or high, using real hazard placements on the China friction surface and the US network distances. Detection follows one of four regimes: rate scaling, delay, delay with frailty, or delay with competing death. For each cell we report bias, root-mean-squared error, and 95% interval coverage of $\hat\beta$ for the naive model, friction-adjusted Cox regression, primary-care restriction, the friction-only ablation, and the full model. We also report the proportion of truly diseased exposed patients each design retains. The decisive pattern for the claim is clear separation from friction-adjusted Cox regression in the delay and competing-death regimes, with parity under rate scaling.

The second experiment is a placebo hazard test on real records. We construct exposure surfaces that track friction but have no plausible biological effect, such as hazard maps shifted to unbuilt or decommissioned sites, or rotated copies of the real map preserving distance to facilities. A correct estimator should return a null effect. If the naive and covariate-adjusted models report "effects" of placebo hazards, that directly shows the bias exists in practice.

The third experiment is anchor agreement on real records. For outcomes with both a sensitive and an insensitive definition, we estimate the exposure effect twice. The sensitive definition is a first outpatient diagnosis. The insensitive definition is admission or death attributed to the same condition, where linkage allows. An estimator that correctly removes access-driven detection should bring the two estimates closer. Divergence that persists after correction would point to the "second delay" mechanism, where distance changes true severity, rather than to detection.

The fourth experiment is a residence-uncertainty check. We rerun the real-data analyses with residences sampled from the imputation distribution rather than fixed at the most likely location, and report how much of the interval width comes from geocoding uncertainty versus detection uncertainty.

The project fails cleanly if three things happen together: friction-adjusted Cox regression matches the full model across the semi-synthetic grid, passes the placebo test, and shows no anchor divergence. That outcome would itself be a useful, citable result for environmental records studies.